FOM: history, funding, etc.

Martin Davis martin at
Tue Aug 3 18:07:37 EDT 1999

Harvey has asked me to comment on his comments on my comments. Frankly, my
first reaction was to be sorry I had got into this. But before plunging in,
I want to make two general further comments (for which I'll also be sorry,
no doubt).

1. Harvey and I write from two fundamentally opposed views of some general
social issues, issues for which f.o.m. isn't really an appropriate forum.
But unless this is understood, our discussion will inevitably be at cross
purposes. My view is that the current situation of scarce resources for
mathematics is artificial and anti-social. Mathematical talent and interest
are rare enough and valuable enough (even from the most crass utilitarian
viewpoint) and the US is blessedly rich enough so there is need for the
perceived scarcity. I remember the post-sputnik days when resources flowed.
We're no poorer today.

I also believe that in conditions of scarcity people will fight ferociously
to defend turf. The kind of contemplation of what is best from a purely
perspective that Harvey (and I) would like to see (with very rare
exceptions) can only be expected to arise when there's plenty to go around.

Of course the top places and top prizes will always be scarce; but getting
them for oneself and one's students would feel much less urgent under
conditions of pleanty. And one can take heart from lots of examples:
Lefschetz did his best work isolated at the Uinversity of Kansas (as he
delighted in telling the students), Weierstrass taught in a secondary
school, Post taught 16 hours per week with no secretarial help or office,
working at home on a desk in his living room.

2. Harvey has presented a schematic picture of the rise and fall of a
mathematical subject. Lots of very smart people (e.g., Marx, Toynbee) have
tried to force history into well-defined schemes, and these work - up to a
point. But human history is so complex and intertwined, that these schemes
turn out to be, in the last analysis, simplistic. History of mathematics is
no exception. Here's a story I encountered recently while working on the
Hilbert chapter for my book (I take the liberty of quoting myself):
The investigation of what came to be called *algebraic invariants*
was initiated by George Boole in one of his early papers.  By
the final quarter of the nineteenth century, algebraic invariants had
become a major focus of mathematical research. Heroic bouts of
algebraic manipulation were brought to bear on the problem of finding
invariants. A true virtuoso in this endeavor was the German
mathematician Paul Gordon, dubbed by his contemporaries the ``king of
invariants.'' Threading his way through thickets of algebra, Gordon
was led to conjecture a simplifying theorem about the structure of
algebraic invariants.  According to Gordon's conjecture, in
considering all of the invariants of a particular algebraic
expression, there would always be a finite number of key invariants
in terms of which all of the others could be expressed by means of a
simple formula.  However, his direct onslaught enabled him to prove
his conjecture only in a very special case.  Gordon's conjecture was
regarded as one of the major problems faced by mathematicians of the
day, and it was generally supposed that the person who managed to
prove it would do so by displaying a virtuosity with manipulative
algebra rivaling Gordon's. In this climate, David Hilbert's proof of
Gordon's conjecture came as a great shock. Instead of complicated
formal manipulations, Hilbert relied on the power of abstract

It was after meeting Gordon himself that Hilbert found himself
captivated by the problem Gordon had set. His solution, found after
six months of work, rested on an extremely general result, known
today as *Hilbert's Basis Theorem*, whose proof was quite
straightforward. Using this ``Basis Theorem,'' Hilbert demonstrated
that the supposition that Gordon's conjecture is false leads to a
contradiction. This spectacular proof of Gordon's conjecture could
not have been satisfactory to Kronecker because of its
non-constructive nature. Instead of furnishing a list of the key
invariants whose existence Hilbert had established, this proof had
merely shown that the supposition of their non-existence would lead
to a contradiction. However, with its demonstration of the power of
abstract thought, Hilbert's proof opened a window on the mathematics
of the coming century. The more general viewpoint uncovered by
Hilbert's proof had the incidental effect of killing the classical
theory of algebraic invariants.  Today, Gordon is mainly remembered
for his reaction to Hilbert's proof.  ``This is not mathematics,'' he
exclaimed, ``it is theology.'' 
Now what killed invariant theory was not its descent into uninteresting
intellectual byways. It was that the technical virtuosity of the experts had
become redundant. Later Hermann Weyl helped to revive the theory, and it is
still alive and kicking.

Here is my scheme, just as simplisitic as Harvey's, but I think revealing
about priority methods: a technique is developed to deal with specific
problems. Experts develop more and more technical virtuosity, and teach the
technique to their students. People fan out looking for problems on which to
try their expertise. Inevitably some of these problems seem esoteric to

Scientists (including mathematicians) are like armies of ants fanning out
over a landscape. As Harvey properly points out most of their proudest
accomplishments are doomed to be forgotten or at best incorporated, as a
small corner of some larger edifice. Remarkably, results criss-cross and
cross fertilisze one another in ways very very hard to anticipate. Think of
what went into FLT. Think of the astonishing Martin-Steel work bringing
together work on large cardianls and on determinacy. On the other hand,
Kreisel and Sacks expected great things of meta-recursion theory,
expectations not (at least so far) fulfilled.

OK. Here goes:
>Davis writes:
>>Efforts to decide in advance which lines of inquiry are productive and
>>policies designed to channel researchers into such lines are fundamentally
>A subject which rejects critical rethinking of its aims and goals, and
>research projects based on such critical rethinking, is itself engaging in
>an "effort to decide in advance which lines of inquiry are *not*
>productive" and is extering a "policy designed to channel researchers *out*
>of such lines." This is typical of subjects at various stages of
>development, as described in my FOM posting "Natural Evolution of Many
>Mathematical Subjects" 11:14AM 8/2/99.
>This is what is fundamentally mistaken and if left unchecked, leads to the
>disintegration of the subject through lack of employment opportunities.
>What is fundamentally not mistaken is an attempt to inject renewal into
>Do you regard a critical examination of the state of a subject, together
>with productive suggestions for renewal, appended with reasons why such
>renewal is needed, as a violation of what you are advocating? Do you want
>to discourage such activity?

I certainly don't want to discourage critical thought especially of the
constructive variety. I object to attacks on a field from the outside.
Constructive suggestions for productive moves should always be welcomed,
whether or not they are called "renewal". But in the nature of things, you
are not going to convince mature mathematicians whose main stock in trade is
virtuosity in a particular technique to abandon that technique. Imagine
telling an accomplished cellist not quite good enough for a solo career to
take up the bassoon.

>>The only worthwhile criterion is the ability of individual
>>researchers. Let them decide what they want to do.
>History shows that the typical researcher celebrated locally in time has
>very little chance of their work becoming important (by any reasonable
>measure) later. Are you against guidance?

Who could be against "guidance." But it is as likely as not to be misguided.

>>My paradigmatic example of fund dispensers deciding how genius should direct
>>its talents is the Dukes of Hannover insisting that Leibniz take as his
>>primary task the researching of their family history.
>Do you think that the current academic environment and government funding
>is really any different than this? Please give us a candid answer to this.

Well hopefully somewhat! But to the extent that it is similar, it is exactly
people proposing "guidance." Why do you suppose that guidance from you will
be listened to more than from the powers that be.

And do remember that the "current" environment is only that: different from
30 years ago (when e.g. the US Airforce was perfectly willing to support
research on Hilbert's 10th problem) and different from what it will be
(better or worse) 30 years from now. This too shall pass!

>Stevenson 1:26PM 7/29/99 provided the following interesting quote from von
>"As mathematics travels far from its empirical source, or still
>more, if it is a second and third generation only indirectly inspired
>by ideas coming from ``reality,'' it is beset with very grave
>dangers. It becomes more and more purely aestheticizing, more and more
>purely {\em l'art pour l'art}. .... In other words, at a great
>distance from its empirical source, or after much ``abstract''
>inbreeding, a mathematical subject is in danger of
>degeneration. At the inception the style is usually classical; when it
>shows signs of becoming baroque, then the danger signal is up.''.
>   J. von Neuman (1943. ``The Mathematician.'' In *In the Works of the
>			   Mind.* Chicago, IL: University of Chicago.)
>When I first read this, I thought that it did not apply to f.o.m. On
>further examination, it does, in the following sense. F.o.m. is
>fundamentally about mathematical thought, and that can be viewed as a
>"reality" or "empirical source." It is particularly evident that in, say,
>reverse mathematics, one is using mathematics itself as an empirical
>source. And there are even major conjectures about this empirical source
>that need to be tested empirically: e.g., the linear ordering under
>interpretation of actual mathematical statements.
>To Davis: What do you think of this quote from von Neumann in light of your

I like "l'art pour l'art"; cf. Hardy for counter opinions. I understand what
von Neumann means, but what was he really fretting about? At the time the
major controversies were over what came to be called soft analysis, Banach
spaces, etc. In fact, these turned out to be very valuable. And as your
example demonstrates, people applying the quote to their own specialty, will
always find underlying empirical sources. Certainly people working in
computability/recursion will have no problem doing so.


                           Martin Davis
                   Visiting Scholar UC Berkeley
                     Professor Emeritus, NYU
                         martin at
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